I'd like to find a suitable research topic (specifically, in mathematics) to work on, where 'suitable' means that it's publishable and amenable to being completed in, say, 6-12 months. While there are plenty of topics I'm interested in and plenty of questions I'd like to answer, I'm not sure how to gauge the difficulty of a topic. I suppose this is normally part of learning to become a researcher in grad school; but while I have a (useless) PhD, my advisor handed me explicit problems to solve and summarily refused to allow me to change them when I'd asked. I'm also in industry now rather than academia (and not even in a real industry-research job), which means that I have little time--- certainly far less than a real researcher--- for useful work. Nevertheless, I'd still like to do whatever I can given my situation, and I can attend a few conferences, retain access to journals, etc.; I just don't have the time or resources that someone in academia would. So, how I can find a specific research topic?

  • A large part of research is simply discovering and clarifying problems to work on. Another part is simplifying them to the state they're still intellectually interesting, their solutions potentially add to the community, and ... are solvable. What's the 6-12 month timeline about? You have your whole life to explore your field. Also by "real researcher" do you mean "professional researcher"? Commented Aug 5, 2021 at 21:37
  • The 6-12 month timeline is an arbitrary scale that would hopefully filter out problems that are too easy or too hard. As for "real researcher," I simply mean one that who can contribute to the field in some nontrivial way, rather than forever bashing my head against problems that are completely untractable or restrict myself to recreational problems (which are fun, but it's the same difference between solving crossword puzzles and being a writer).
    – anomaly
    Commented Aug 5, 2021 at 21:48

3 Answers 3


"I'd like to find a suitable research topic (specifically, in mathematics) to work on, where 'suitable' means that it's publishable and amenable to being completed in, say, 6-12 months."

Sorry to disappoint you, but that is not how mathematics works. If you are a professional, the possibility to produce a steady flow of results comes not from your ability to estimate the time needed for each particular project but from the general approach which is a combination of some pieces of folk wisdom like "cut the tree that matches your strength" and "don't put all your eggs into one basket". If you are an amateur, it comes from the sheer enthusiasm and the fresh point of view on things (also available to and important for a professional, BTW, but playing secondary role to a methodical approach there).

In both cases, the first question you asked is just meaningless (for that simple reason that no random person on the web can even approximately estimate your strength or tell which topics will carry you away and which won't, if you do not want to invoke higher level considerations). Either learn to live in the ever-shifting treacherous alternative reality based on the crazy concoction of high and low speeds, short euphoric moments and long depressive periods, persistent pressure and all-out spurts, rational calculations and pure luck, or consider another career path taking some "safe" job where the result is directly proportional to the product of the time and the effort spent.

As to your second question: "How to find a topic to research?", you don't find the topic; rather it finds you. Just go around and read papers you can understand and talk to mathematicians you know about what they are doing. Everybody is stuck with some "little thing" that does not require too much time to explain and if you can help someone to get unstuck in their project, you may easily get three things at once: a reputation, a joint paper, and a friend.


While I agree to some extent with fedja, I think it is possible to actively choose problems that you can finish in a relatively short time frame. Here are general and specific suggestions.

  1. Choose your problems carefully. You can only make gauge how long a problem will roughly take you to make progress if (a) you understand what has already been done and (b) you have a fairly clear plan of how to make progress. This means you may spend weeks or months going through potential ideas for problems before you come across one you like that you have a plan for solving. Such plans could come from being something similar you've done before or following the strategy of a previous paper.

  2. Ask other mathematicians. This could be another professor you had or a maybe fellow grad student. It's possible they have more problems than time to work on (I know I do), and some of them may be rather clear cut.

  3. Read the (Amer. Math.) Monthly. If you're not too focused on a certain area, the Monthly is a good source of ideas for problems which don't require too much background to understand. I sometimes look at the there for ideas for problems for undergrads or high school students. While a lot of articles in the Monthly aren't so "deep" (some are), many of them are very interesting, and can suggest similar projects (which can be publishable in normal journals). Since you're not "in academia" anymore, I'm guessing you're wanting to do this for your own enjoyment, and you can do fun research that isn't necessarily deep.

  4. Check out questions on MathOverflow and Math.SE. (I'm just mentioning this since we're on SE now, but I think the Monthly is a better approach.) People ask interesting questions many of which are unanswered, and I've gotten ideas for little projects from these sites(none of which I've done, of course--but other people have). (Unanswered doesn't mean the answer's not in the literature, but for a few questions it's pretty clear it's not.) Of course, you will often need to do a serious literature search, because the right references may not be given to you as they are likely to with Monthly articles.

  • Thanks. I should mention, though, that my problem is not finding a problem I understand; it's finding one that's deep enough to be interesting but wouldn't involve wasting years I don't have looking for a solution. (There are lots of nasty open combinatorics problems, for example, that are easy to write down but quite difficult to solve.) In other circumstances, I'd prefer a broader research topic than looking for a specific, bite-size problem to solve; but, Fedja's condescending response notwithstanding, I'm stuck because of my situation with the latter.
    – anomaly
    Commented Jun 25, 2015 at 14:55
  • @anomaly I understand, but I'm saying there are lots of Monthly articles where there are natural extensions of the work done there where at least a rough plan of attack is already there. Then thinking about it for a few days should give you a sense of whether things are likely to work out. If you start with a sufficiently interesting "bite-size" problem, it can easily lead into a whole research area for you.
    – Kimball
    Commented Jun 25, 2015 at 15:44

While I am in a completely different field, what I would recommend you is participating local conferences, seminars in your area. Universities also regularly invite famous speakers, go learn, ask questions, talk to them.

This is a good way to see what kind of research topics other people do, and good way to find possible mentors or at least useful comments on possible research topics.

On the other parts I agree with fedja: there is no magic wand that tells you how long a project will be, especially if you are new at the field. These are not home-work assignments where people know beforehand the answer, the difficult and possible pitfalls. If it is a project that you can finish and publish in 6 month in spite you have no time to research, maybe it is not a particularly difficult project. But can lead you better ones on the long run, and lead to other projects.

  • I'm not new to the field, and I realize how research works. But I'm not in the situation now of being able to devote myself full-time to research, so I want to at least carve off a modest problem and make progress on it.
    – anomaly
    Commented Jun 25, 2015 at 4:49

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